…or they’ll say “see, that’s why we need to lower the standard for power from 80 percent! Even studies with p=0.05 don’t achieve 80 percent power! From now on let’s use 50 percent power!”
Darkness cannot drive out darkness; only light can do that.
Hate cannot drive out hate; only love can do that.
In all seriousness, I wish to ‘preregister’ the conjecture that what’s most needed is a sympathetic reading of Bababekov et al. That is, I suspect the ‘debunking’ has to begin with an appreciation for whatever legitimate aim they were hoping to achieve.
i hadn’t though of that, youre probably right
I’ve actually tried that. In the letter that @zad and I submitted in response to their prior paper at Annals of Surgery - which has been accepted but is not yet in print, b/c according to the journal it has been sent to the authors so they can reply (again!) - we offered a better solution for what they’re proposing - namely, that rather than computing an “observed power” based on the study effect size, that they could report the “power” the study would’ve had to detect a modest difference that may have been clinically relevant, with an example. I’m on my phone right now and don’t have that full paper handy, but appreciate what you say and would note that we, along with the others who responded to their initial papers (Gelman in particular) tried to tell them “we get what you’re going for, but this is the wrong way to do it; here’s a (slightly) better way.” This has, to my mind, been tried. Again, if you feel that you have a better way of reaching them, I would be MORE than happy if you can achieve this.
Thanks, I didn’t know that Epidemiology had such a policy. Will submit the rejected LTE there and see what happens.
"Despite statisticians warning against the use of observed power for decades (Hoenig & Heisey, 2001), the practice continues, usually from research groups who are unaware of the problems with it. Bababekov et al. (the authors of this paper) have not only defended their use of observed power in previous papers, even when criticized by statisticians who have looked into the problem, but unfortunately, they encourage others in surgical science to do the same.
The arguments put forth in this paper have no mathematical or empirical basis. Meaning, Bababekov et al. have not given any mathematical proofs or simulated data to make their case. Their argument merely consists of,
“Although it has been argued that P value and post hoc power based on observed effect size are mathematically redundant; we assert that being redundant is not the same as being incorrect.”
“We believe this redundancy is necessary in the unique case of surgical science, as post hoc power improves the communication of results by supplementing information provided by the P value.(12) Moreover, post hoc power provides a single metric to help readers better appreciate the limitation of a study.”
The problem is that this practice is not only redundant, it is incorrect and highly misleading. This can easily be shown with simulated data (see attached image). Here, I simulate 45,000 studies from a normal distribution and where I have set a true between-group difference of d = 0.5.
Group A has a mean of 25 and standard deviation of 10, and group B has a mean of 20 and also a standard deviation of 10. Thus, (25-20)/10 gives us a standardized effect size of 0.5. This is the true effect size, something we would rarely know in the real world (the true effect size is unknown, we can only attempt to estimate it).
In this simulation, the studies can be categorized by nine different sample sizes, meaning they have varying true power (something we know because it’s a simulation). True power ranges all the way from 10% to 90% and each of the nine scenarios has samples simulated from a normal distribution.
The graph above has some random variation added between points to make them out, but in reality, this (below) is what the graph looks like without any random variation at all. (These are not lines, but actual points plotted!)
The transitions can also be seen here:
Notice that despite true power being known for each of these studies, observed power highly varies within these scenarios, especially for studies with low(er) power. For example, when true power is set at 10%, many studies yield results showing “observed power” of 50%. Therefore, if we were to follow the recommendations put forth by Bababekov et al. in several scenarios, we would mistakenly put more confidence in results that truly have low power and which yield noisy estimates. Meaning it is not reliable in “improving the communication of results”.
This is because Babakev et al. does not seem to understand long-term frequencies. Statistical power is a frequentist concept, meaning that if someone designs a study with the hope of the test correctly detecting a dimensional violation by the test hypothesis (such as the null hypothesis) 80% of the time, this will occur in the long term if there is a violation of assumptions and given other assumptions.
This does not mean that the study itself has an 80% probability of correctly detecting a violation. For example, when we say that a fair coin has a 50% probability of getting either heads or tails, it does not mean we expect the coin to always give us results that fairly balance the distribution of heads and tails. We will not always expect alternating results of heads and tails (H T H T H T). In fact, it is very plausible that if we flip the coin 10 times, we may get all heads or all tails. However, in the long term, we expect the proportion of heads and tails to be fairly equal.
Furthermore, because the P-value is a random variable and measures random error in the estimate (Greenland, 2019), taking it (observed P) from a single study and transforming it into a distorted version of power (observed power) is beyond fallacious. The authors not only confuse observed power and true power, but they also confuse the random variable P with its realization, observed P. Observed P-values are useful because they indicate statistical compatibility between the observed data and the test hypothesis.
If they are being used for decision rules with a set alpha, and the researchers suspect that a type-II error was very likely, they can use the computed confidence/compatibility/consonance intervals to see what effect sizes are within the interval and how wide the interval estimates are (which measure random error/precision).
However, Bababekov et al. does not see this as a solution as they argue here,
“An alternative solution to mitigate risk of misinterpreting P > 0.05 is for surgical investigators to report the confidence intervals in their results along with the P value.”
“However, the general audience would likely pay more attention to the overlap of confidence intervals in a comparative study with two or more comparison groups with multiple confidence intervals, and still misinterpret the findings as demonstrating equivalency.”
The problem here is that investigators confusing overlapping intervals for equivalency is a cognitive problem (Greenland, 2017) where they do not understand what frequentist intervals are rather than a defect in the method itself.
A computed frequentist interval, such as a 95% confidence/consonance interval contains all effect sizes that yield P-values greater than 0.05 (Cox, 2006). Of course, the computed point estimate, often the maximum likelihood estimate (MLE), has the largest P-value, and values close to it, which will have slightly smaller P-values than the MLE, indicate greater statistical compatibility than effect sizes that are further from the MLE, which will have much smaller P-values.
Thus, it is largely irrelevant whether two or more confidence/consonance intervals overlap. The useful questions are:
- how wide are these intervals?
- how much do they overlap?
- what effect sizes do they span?
Better than computing a single interval estimate for a particular alpha level is to compute the function, where every interval estimate is plotted with its corresponding alpha (10%, 15%, 25%, 50%, 90%, 95%, 99% confidence/consonance intervals), since the the 95% interval is largely arbitrary and a relic of NHST with a 5% alpha.
Bababekov et al. instead sees observed power as being a solution to the “problems” they highlight with interval estimates,
“Power provides a single metric to help readers better appreciate the limitation of a study. As such, we believe reporting power is the most reasonable solution to avoid misinterpreting P > 0.05.”
This argument further highlights the problems with trying to come to conclusions from single studies. The authors wish to answer
“Was my study large enough and reliable, and if not, what single metric can I use to better understand how reliable the decision (reject/fail to reject) is?”
For this, they have found a method, one that they reify, that helps to address their uncertainties of the data-generation process, but unfortunately, it is unreliable and cannot do what they wish it does.
As others have pointed out above, the arguments put forth in this paper are fallacious and thus the manuscript itself is defective and has the potential to seriously mislead many surgical investigators who are not well versed in statistical methods. Letters to the editor (of which there are numerous) and corrections are simply not enough. A retraction is necessary when a manuscript is this defective."
edits: some formatting and added link to the original publication
second update: included two visualizations, one with random variation between points to make out the points and not confuse them for lines, and one without any jitter
third update: added a gif to show transitions
Wow this is fantastic @zad! My only suggestion is to note that power can’t be observed. So I would put observed in quotes everywhere and explain that power depends on unobservables (both a test statistic yet to be observed and an effect size that is a hypothetical).
It is unfortunate to see that the author has also published other similar articles arguing for post-hoc power.
Having worked with many physicians, I can’t say I’m surprised that the surgeons are the ones using the “because I said so” argument to say “it’s not wrong.”
It seems like they’ve missed the boat when they ask for reconsideration of the arbitrary 80% level, but then, rather than discuss education on how to use the procedure and actually consider trade-offs of Type I and Type II errors, they skirt this entirely and say “I want this to work, so this is our solution, which has no basis in reality.”
I hope your rebuttal is published and their paper is retracted. If you look in their references, their other papers on this topic should be retracted, too.
This reminds me of an excellent quote (I wish I remember from whom) to the effect that we need the let surgeons know that we want to learn how to do complex surgery in our spare time as biostatisticians.
Senn said this on twitter recently but didn’t attribute it to anyone…
Frank, I recall that one of your co-panelists at an JSM panel a few years back told this story. He got a call from a neurosurgeon who explained, “I’m doing a trial, but I don’t need your help; I’ll do my own stats. Can you suggest a good stats book?”
The statistician said, “I’m so glad you called! I’ve always wanted to do brain surgery; can you suggest a good book on that?”
i feel like something similar is happening with the fragility index. There is some analogy in evolution: we’re headed in a certain direction, we’re stuck the the p-value/hopthesis testing and we just build on top of it. Was it Gould’s panda’s thumb, or dawkins landscape of peaks and valleys, there’s an anology somewhere
Oddly, I find it is surgeons who are the most inflexible and most difficult to discuss any of this with logically. The reason I say “oddly” is because of how much they appreciate hierarchy, specialization, and rigor of training-- just seemingly they are the jack of all trades and master of all so they run every field (in their minds). I don’t like making these generalizations, but I haven’t had as many negative experiences with non-surgeons. Internists and other specialists seem to be more willing to accept they’re not the authority on everything beyond their scope.
I’m not sure how to combat it after many attempts.
There must be a way of converting these disputes into a betting game, letting the surgeons set the odds, and taking the opposite side. I’d have to think about this a bit more to come up with an appealing gamble for them, but clearly negative expected value.
Their informal mental model seems to be one that it can be easily “Dutch Booked” in that they will take the same data and draw different conclusions based upon an irrelevant alternative (ie. post hoc power).
I think a lot of fun can be had making this a bit more public. Economist Bryan Caplan (George Mason University) currently has an undefeated 17-0 track record when making other academics back up their prognostications with actual money.
I would love to see this. But, physicians are notoriously poor with money, so this will be another area where they might lose money!
On the observability of power: are my analogies correct?
Analogy one: the telescope.
“Using a sample to estimate both the population effect and (observed) power, is like taking a picture of the sky and using that to estimate both the average brightness of the stars and the sensitivity of the telescope. This is not possible. Or you use an instrument of known sensitivity and you estimate the population effect, or you calibate the instrument using a known population”
Analogy two: the fuel gauge.
“You cannot look at the fuel gauge and estimate from that both how many liters of fuel you have left and the sensitivity of the gauge. Either you take a calibrated gauge and you estimate how much fuel is in the tank, or you use a known amount of fuel to calibate the gauge”
As far as I know frequentism cannot answer the question “how likely is hypothesis X given the data”. Or am I misreading you?
Please help me understand this! What different conclusions about the parameter would you draw if the intervals are wide versus narrow?
Edit: a compatibility interval is (usually) just a standard error times some number, right?
I have no idea what I wrote there. What I meant to say was that failing to reject the null hypothesis by getting an observed P greater than a prespecified alpha is not enough to rule out a difference. For more support of the null hypothesis, one must use equivalence testing. And depending on how they set it up, it could be used to rule out meaningful effects. But this is all more idealistic than anything, given that equivalence testing can often have problems of its own.
Given that interval widths decrease with more available sample information and become more informative about the parameter, an interval that is narrow is far more informative than an interval that is wide.
Care to comment on the following:
Fallacy 2 (The Precision fallacy)
The width of a confidence interval indicates the precision of our knowledge about the parameter. Narrow confidence intervals correspond to precise knowledge, while wide confidence errors correspond to imprecise knowledge.
There is no necessary connection between the precision of an estimate and the size of a confidence interval.
I would agree that, given an infinite N, the CI converges to a point. But I think I understand the author’s broader point – for any finite sample, a CI is a random interval, and the width is in some sense, a random number. The precision of our estimate is contingent on nothing more than the size of our sample, which is only related to the width of the interval “in the long run.”
Someone please correct me if I am wrong.
You are right. Personally I see a confidence intervals as a descriptive statistic. Most of the time, a 95% CI is simply x̄ ± (1.96 * SE). So it is a summary of the data.
Sometimes your datapoints are close together. Then you have a narrow CI. It happens.